A Phase II/III Study of SEP-190 (Eszopiclone) in Patients With Primary Insomnia (Study 190-126): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Phase II/III Study of SEP-190 (Eszopiclone) in Patients With Primary Insomnia (Study 190-126) (NCT00770510), a randomized phase 2, phase 3 study. The primary outcome is Latency To Persistent Sleep (LPS).

2. Clinical Question

3. Trial Design

The registry record describes a Phase II/III, randomized, double-masked, crossover study sponsored by Eisai Co., Ltd. Its stated purpose was to investigate and evaluate eszopiclone in Japanese participants with primary insomnia. The study is marked completed. The record lists enrollment of 192, a start date of 2008-09, and primary completion in 2010-05.

Five treatments are listed: eszopiclone 1 mg, 2 mg, and 3 mg; placebo; and zolpidem Tartrate 10 mg. The crossover designation means treatment comparisons are associated with a design in which participants may receive more than one study treatment over time. However, the registry record does not report the treatment sequences, the duration of each treatment period, any washout intervals, or how period and sequence effects were incorporated into the analysis. Those details should not be inferred from the design label alone.

The primary outcome was latency to persistent sleep, measured in minutes using polysomnography. Its timeframe is described as 10 days comprising five intervals of two consecutive nights. Recording was scheduled in relation to each participant’s median bedtime as recorded in a sleep diary, and treatment-period recordings were centrally scored by a trained expert. The outcome population was the full analysis set, defined by randomization, receipt of at least one dose, and evaluable primary efficacy data from any of the five intervals.

The registry record does not report the trial’s original sample-size justification, its prespecified statistical analysis plan, or details of its handling of crossover-specific effects. These omissions limit how closely the posted arm summaries can be connected to the intended design-based analysis.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: Of the 192 participants who entered the screening period, 72 were randomized to study medication (excluding 119 ineligible participants; one withdrawal of consent).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set: includes randomized participants who were administered \>= 1 dose of study medication and had evaluable data for the primary efficacy assessments from any of the 5 treatment intervals.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Latency To Persistent Sleep (LPS), measured over 10 days (5 intervals of two consecutive nights).

Latency to persistent sleep (LPS) is the time, in minutes, taken to fall asleep according to the endpoint definition. The registry record describes it as an objective measure based on polysomnography (PSG), an overnight recording used to assess sleep. Recording duration for scoring was 8 hours. PSG timing was individualized and scheduled within +/- 30 minutes of the participant’s median bedtime in the sleep diary; a diary was used during screening to record lights-out time before PSG evaluations. Treatment-period PSG data were centrally scored by a trained expert.

As a continuous measure, LPS is summarized by a mean and standard deviation. The mean describes the group’s average measured latency, while the standard deviation describes variability among observations around that average. In general, sleep-onset latency is useful as a direct measure of how long it takes to fall asleep; that is a general explanation of the measure, not an additional trial finding.

The listed timeframe is 10 days, arranged as five intervals of two consecutive nights. The registry record does not explain how measurements from multiple intervals were combined into each posted group mean, or how dependence among repeated observations was handled. It also does not report a separate endpoint-level analysis population beyond the full analysis set definition.

7. Results Posted in the Registry

• Eszopiclone 1 mg: mean 24.40 versus 37.50 on control; difference -13.10 (95% CI -23.38 to -2.82), standardized effect d = -0.42; z-test p = 0.012.
• Eszopiclone 2 mg: mean 20.90 versus 37.50 on control; difference -16.60 (95% CI -27.10 to -6.10), standardized effect d = -0.52; z-test p = 0.002.
• Eszopiclone 3 mg: mean 12.80 versus 37.50 on control; difference -24.70 (95% CI -33.89 to -15.51), standardized effect d = -0.88; z-test p = <0.001.
• Zolpidem Tartrate 10 mg: mean 14.30 versus 37.50 on control; difference -23.20 (95% CI -33.46 to -12.94), standardized effect d = -0.74; z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

What does a mean and standard deviation describe?

The primary endpoint is continuous and is reported as a mean with a standard deviation. In general, a mean is the arithmetic average of measured values in a group. A standard deviation describes how dispersed those values are around the average. A larger standard deviation indicates more spread in the measurements; it is not the uncertainty of the mean itself. The reported group standard deviations are 37.8 minutes for placebo, 22.7 minutes for eszopiclone 1 mg, 24.3 minutes for eszopiclone 2 mg, 11.2 minutes for eszopiclone 3 mg, and 22.6 minutes for zolpidem Tartrate 10 mg.

The mean difference expresses the estimated separation between a treatment-group mean and the placebo mean. Negative values in these comparisons indicate a lower mean LPS in the named treatment group, because the posted comparison is treatment minus placebo. For example, the recalculated estimate for eszopiclone 1 mg is -13.1 minutes. This is a difference between group averages, not a statement that every participant’s latency changed by that amount.

How should the recalculations be understood?

The comparison estimates and confidence intervals are simple unadjusted recalculations from the posted summary statistics. They are not a substitute for an analysis that accounts for the trial’s design and prespecified methods. The registry record lists zero analyses and does not describe a sponsor model for the primary outcome. No discrepancy is flagged between the posted summaries and these recalculations, but the absence of a reported analysis still means that design-specific inference cannot be checked from the registry record.

In general, a randomized crossover study can yield comparisons in which participants receive different treatments across periods. Analyses may need to account for repeated observations within a participant, treatment period, sequence, and possible carryover. These are general considerations for crossover designs, not claims about what occurred in this trial. The registry record does not report whether such factors were modeled, whether carryover was assessed, or how period measurements were used to form the displayed means.

What do p-values and confidence intervals add?

A p-value, in general, measures how incompatible the observed data are with a specified null hypothesis under the assumptions of the statistical test. It is not the probability that the null hypothesis is true, and it does not measure clinical importance. The recalculated unadjusted p-values are 0.012 for eszopiclone 1 mg, 0.002 for eszopiclone 2 mg, and <0.001 for both eszopiclone 3 mg and zolpidem Tartrate 10 mg. They do not show whether a multiplicity procedure was applied; the listed values are explicitly unadjusted.

A confidence interval gives a range of values compatible with the data and the method used to calculate it. In general, it reflects uncertainty in the estimated mean difference. Here, the reported intervals were recalculated from summary data, so they may not capture uncertainty from crossover-specific features that cannot be assessed from the registry record. A confidence interval is not a range containing a fixed proportion of individual participant outcomes.

Why can repeated measurements matter?

General statistical reasoning: observations from the same participant over time are often correlated rather than independent. Treating them as independent when they are not can make uncertainty estimates inaccurate. Crossover analyses can also distinguish treatment effects from changes related to period or treatment order. The registry record identifies a crossover design and five treatment intervals, but does not describe its treatment sequences or model. The recalculations therefore should be read as comparisons based on posted group summaries, not as a reanalysis of the complete repeated-measures data.

Over-dispersion is a general concern when observed variability is greater than a statistical model assumes; it can lead to uncertainty estimates that are too narrow if not accommodated. The primary endpoint is continuous, and the registry record reports standard deviations, but it does not identify an over-dispersion assessment or model. That concept is not a specific reported finding in this study.

What is known about the analysis population?

The full analysis set includes randomized participants who were administered at least one dose and had evaluable primary efficacy data from any of the five treatment intervals. This definition does not mean that every randomized participant contributed an observation to every interval. The record does not state how many measurements were missing, how incomplete intervals were handled, or whether imputation was used. It also does not report a per-protocol population or a safety-analysis population definition beyond the group-level counts.

In general, missing outcome data can affect both the estimate and its precision, particularly if the chance of missingness is related to the outcome. Without a reported missing-data method or interval-specific flow, the effect of missing measurements cannot be evaluated from these summaries. Likewise, the posted group counts should not be interpreted as proof that each treatment period had complete endpoint data for all participants assigned or exposed to that treatment.

What do the summaries not establish?

The registry record does not report the original sample-size justification, interim analyses, statistical analysis plan, or multiplicity adjustment. These absences mean the recalculated results cannot establish whether the trial’s own planned hypotheses and model were followed. The sample-size illustrations are separate planning exercises based on observed effects, not an account of the original design. Statistical results should therefore be interpreted alongside the endpoint definition, the stated analysis population, and the limits of the registry’s reporting.

10. Confidence Intervals and Precision

Precision is reflected in the width of a confidence interval: narrower intervals indicate less uncertainty about the estimated mean difference under the calculation method, while wider intervals indicate more. In general, an interval does not show the range of individual participant responses, and it does not assign a probability to a particular fixed treatment effect.

The recalculated 95% confidence interval for eszopiclone 1 mg versus placebo is -23.38 to -2.825 minutes. For eszopiclone 2 mg, it is -27.1 to -6.103 minutes; for eszopiclone 3 mg, -33.89 to -15.51 minutes; and for zolpidem Tartrate 10 mg, -33.46 to -12.94 minutes. Each interval is on the negative side of zero, consistent with a lower mean LPS in the named group in these recalculations. The intervals still allow a range of possible mean differences, so their endpoints should be considered along with the point estimates.

These intervals are unadjusted recalculations from posted summary statistics. The registry record does not report a sponsor analysis, the treatment-period model, or adjustment for multiple comparisons. As a result, the intervals do not establish the precision of a design-specific crossover estimate or account for any multiplicity procedure. They also cannot address uncertainty arising from missing data or other unreported analysis choices.

Group sizes for the posted comparisons range from 68 to 71 participants per treatment group. Standard deviations differ across groups, as do the interval widths. In general, precision depends on sample size and variability, but the group summaries alone cannot establish whether the methods fully reflected repeated measurements within participants. The confidence intervals are best read as uncertainty ranges for the stated unadjusted recalculations, not as a complete account of all sources of uncertainty in the trial.

11. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm, not total events. The registry record’s planning illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses an effect to detect equal to the stated fraction of the observed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a future two-arm study to have an 80% chance of detecting the specified effect under those planning assumptions, if that effect and the assumptions are correct. The 90% power column gives the corresponding planning number for a 90% chance. These are design calculations, not guarantees: actual performance depends on the true effect, variability, analysis method, and whether the planning assumptions hold.

Rows based on 100%, 75%, and 50% of the observed effect represent planning for progressively smaller effects. A smaller effect is generally harder to distinguish from random variation, so the illustration requires more participants per arm as the assumed effect gets smaller. The displayed planning curves should be read in the same way: they illustrate how the estimated requirement changes with the assumed effect size, rather than reporting trial outcomes.

These are planning illustrations based on the observed effect, not observed power. They do not show the probability that the completed study’s result is true, and they do not recover the trial’s original design rationale. They also use a two-arm equal-allocation setup, whereas the registry record identifies a crossover study with multiple treatments; the illustration is therefore not a reconstruction of the original crossover design.

12. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -13.100; pooled standard deviation σ = 31.231.
2. n = 2 × (1.96 + 0.842)² × 31.231² / -13.100² = 89.2, rounded up to 90 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -13.1                      # observed difference in means
sigma <- 31.2306124032036                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(770510)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 90 (80% power), 120 (90% power)
 75% of observed effect: n per arm = 159 (80% power), 213 (90% power)
 50% of observed effect: n per arm = 357 (80% power), 478 (90% power)
power.t.test: 90.2 
Simulated power at n = 90 per arm: 0.800 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

13. Multiplicity, Missing Data and Analysis Populations

Four secondary outcomes are listed: total sleep time, sleep efficiency, wake time after sleep onset, and number of awakenings, each with objective and subjective forms noted in the record. The primary endpoint is LPS. Six outcome measures are reported in total, but the registry record lists zero analyses. It does not provide results for the four secondary outcomes in the information, nor does it describe a hierarchy of outcomes or distinguish confirmatory from exploratory analyses.

Multiple comparisons raise a general statistical issue: when several hypotheses are tested, the chance of at least one apparently unusual result can increase if each test is evaluated separately. The posted p-values for the treatment-versus-placebo LPS comparisons are unadjusted. The registry record does not report a multiplicity correction, a gatekeeping strategy, or another method for controlling the overall error rate. The p-values should therefore be read as unadjusted rather than as evidence that multiplicity was addressed.

The full analysis set is defined as randomized participants given at least one dose and with evaluable primary efficacy data from any of the five treatment intervals. The record does not report how many participants lacked evaluable outcome data, how missing observations were handled, or whether imputation or sensitivity analyses were used. It does not describe whether participants with only some evaluable intervals contributed to each treatment comparison in the same way.

The record also does not report a detailed analysis population for safety or a separate per-protocol set. Because the study is identified as a crossover, handling of sequence, period, and within-participant correlation could matter to inference; the registry record does not describe the model or related checks. These reporting gaps make it difficult to determine how the recalculated summaries relate to a prespecified analysis or how robust the comparisons are to missingness and multiplicity.

14. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 2% reporting threshold.

Most frequent non-serious adverse event terms

The registry record reports serious adverse events for each listed group. The serious adverse event count is 0 for placebo, 0 for eszopiclone 1 mg, 0 for eszopiclone 2 mg, 0 for eszopiclone 3 mg, and 0 for zolpidem Tartrate 10 mg. These counts are reported among group sizes of 71, 70, 69, 68, and 70, respectively. The record lists no serious adverse event terms. Deaths are not reported in the registry record.

These are group-level registry counts. They describe what is reported for the listed groups, but they do not establish that no serious events could occur or provide information about events not captured or not reported. Because the design is crossover, the group counts should not be added to estimate a number of distinct participants; the registry record does not report participant overlap across treatments or detailed safety follow-up by period.

The record also lists other adverse events affecting 5 participants in the placebo group, 10 in the eszopiclone 1 mg group, 10 in the eszopiclone 2 mg group, 17 in the eszopiclone 3 mg group, and 8 in the zolpidem Tartrate 10 mg group. Those are separate from the serious-event counts and should not be conflated with them. The registry record does not provide further detail on the types or severity of these other events in the information.

15. What the Result Does, and Does Not, Mean

The posted primary outcome summaries describe measured latency to persistent sleep in a randomized, double-masked crossover study of Japanese participants with primary insomnia. The mean was 37.5 minutes for placebo and ranged from 12.8 to 24.4 minutes across the three eszopiclone groups; the zolpidem Tartrate 10 mg mean was 14.3 minutes. The unadjusted recalculated comparisons with placebo were negative, with the intervals reported entirely below zero. This is a statistical description of the posted endpoint data, not medical advice or a conclusion about treatment for an individual.

The results do not show that every participant had a shorter latency, nor do the group means describe the distribution of individual outcomes. The standard deviations indicate variability within groups. The registry record does not report the complete participant-level data, treatment sequences, crossover model, or handling of incomplete measurements, so the summaries cannot establish how those features would affect a design-specific analysis.

The reported p-values are unadjusted, and no multiplicity method is reported. The recalculated confidence intervals quantify uncertainty under their calculation method, but do not account for unreported crossover modeling or missing-data decisions. Thus, these estimates should not be treated as a substitute for a prespecified sponsor analysis, which is not reported in the registry record.

The findings are limited to the stated primary endpoint and its specified analysis population. Four secondary outcomes are listed, but their results are not included among the posted comparisons. The record does not report long-term outcomes, effects beyond the stated study timeframe, or a basis for generalizing beyond the study population. Statistical significance alone does not establish clinical importance; the registry record does not report a threshold for a meaningful change in LPS.

16. Why This Trial Matters Statistically

This study is statistically notable for combining multiple treatment comparisons with a crossover design and repeated endpoint intervals. Such designs can make within-participant comparisons informative, but their analysis depends on how treatment order, period, repeated observations, and possible carryover are handled. The registry record identifies five intervals and a crossover model, yet does not report the model or sequence details. That makes the distinction between a posted summary comparison and a design-aware trial analysis especially important.

The primary endpoint is an objectively assessed continuous measure, and the record reports means and standard deviations for the treatment groups. Those summaries allow straightforward unadjusted comparisons with placebo and confidence intervals, but do not capture every design feature. The recalculated mean differences are negative for each listed comparison, and their intervals are below zero. Interpreting those numbers responsibly requires keeping their unadjusted status and the absent crossover analysis details in view.

Multiplicity also matters because several treatment comparisons and secondary outcomes are part of the record. The listed p-values are unadjusted, and no correction or outcome hierarchy is reported. The record therefore illustrates why effect estimates, confidence intervals, and analysis-plan information should be considered together rather than relying on a p-value alone.

Finally, planning requirements based on an observed effect are not retrospective evidence of a study’s power. The planning illustration can help readers understand how assumed effect size affects future sample-size requirements, but the trial’s original design justification is not reported. The distinction between observed results, recalculated inference, and future planning is central to an accurate statistical reading.

17. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Several trial-specific details needed to interpret the posted comparisons are not reported in the registry record. Although the study is labeled crossover, the treatment sequences, period lengths, washout intervals, and method for addressing period, sequence, or carryover effects are not described. The record also does not explain how observations across five intervals were combined for the reported means or whether repeated measurements within participants were modeled.

The registry record does not report the sponsor’s statistical analysis for the primary endpoint, an original sample-size justification, interim analyses, or the analysis plan. The comparisons discussed are simple unadjusted recalculations from group summaries. They cannot reproduce a crossover model or establish whether the intended analysis reached the same estimates or uncertainty.

Missing-data details are also absent. The full analysis set requires evaluable primary data from any of the five intervals, but the record does not state how many participants had incomplete intervals, how missing observations were handled, or whether sensitivity analyses were performed. Outcome reporting is limited in the record: four secondary outcomes are listed, but their results are not included in the posted analyses.

The confidence intervals and p-values for the treatment comparisons are unadjusted, and multiplicity handling is not reported. The record also does not supply a threshold for interpreting a change in LPS as clinically meaningful. These limitations do not negate the posted summaries; they delimit what can be concluded from them and distinguish the recalculations from a complete trial analysis.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: A Phase II/III Study of SEP-190 (Eszopiclone) in Patients With Primary Insomnia (Study 190-126) — NCT00770510.
• Registry record last updated 2013-02-04; status last verified 2012-12.
• Results first posted 2013-02-04.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

21. Record Summary

The registry record describes NCT00770510 as a completed Phase II/III randomized, double-masked crossover study sponsored by Eisai Co., Ltd. It enrolled 192 participants with primary insomnia and stated a purpose of evaluating eszopiclone in Japanese participants. The listed treatments were eszopiclone 1 mg, 2 mg, and 3 mg, placebo, and zolpidem Tartrate 10 mg.

The primary endpoint was polysomnography-measured latency to persistent sleep in minutes, over 10 days arranged as five intervals of two consecutive nights. Posted group means were 37.5 minutes for placebo, 24.4 for eszopiclone 1 mg, 20.9 for eszopiclone 2 mg, 12.8 for eszopiclone 3 mg, and 14.3 for zolpidem Tartrate 10 mg. The treatment comparisons are unadjusted recalculations; the registry record lists no analyses.

Four secondary outcomes are listed. The record reports 0 serious adverse events in each group. The original sample-size rationale, crossover analysis details, multiplicity handling, and missing-data methods are not reported in the registry record.